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Withdrawn from ICLR 2027

Recall Is Not Evidence Use: Objective Imprinting in Retrieval-Augmented Systems

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Retrieval recall measures whether supporting evidence enters the context, while downstream behavior also depends on the policy that uses that evidence. When semantic evidence and retrieval metadata agree, evidence-reading and rank-following policies are observationally indistinguishable under ordinary accuracy. We study this ambiguity through policy identifiability and define objective imprinting: the persistence of a history-selected policy when later supervision remains task-correct while ceasing to distinguish among compatible rules. In paired histories, semantic and proxy policies remain latent behind identical agreement-set performance through 64k shared-example presentations. In source-disjoint full-corpus retrieval, this distinction has a large downstream consequence: Recall@4 reaches 99.2%, while recoverable rank errors yield an 82.8-point mean exact-match gap under a common reader. Holding retrieved passages and display order fixed, changing only rank metadata reverses proxy routing and isolates evidence use from evidence availability. Policy-identifying supervision also provides direct control: 40 cue conflicts reliably rewrite either policy while preserving agreement-set accuracy. Together, these results separate evidence availability, observed-task performance, and evidence-use policy, and show how identifying information can expose and steer the policy governing retrieved evidence.

Primary area:
interpretability and explainable AI
Keywords:
Objective Imprinting, Policy Identifiability, Evidence Use, Mechanistic Interpretability

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
Reviewer_BK9UOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies whether models can retain different evidence-selection policies despite achieving identical accuracy on subsequent training data. Paired models are initially trained to follow either semantic evidence or a metadata cue, then receive identical examples on which both cues agree. The resulting policy difference persists through 64k shared-example presentations. A retrieval experiment further shows that changing rank metadata while holding retrieved passages fixed can substantially alter source selection and downstream answers. The paper also examines parameter interpolation, weight and activation interventions, and whether small sets of cue-conflict examples can rewrite the learned policy.

Critical strengths
  • The rank intervention is well controlled. The passages and their display order stay the same while only the rank metadata changes. This makes the effect of metadata easy to interpret. Using the same downstream reader also helps connect source-selection errors to answer quality.

  • The controlled findings are supported by several complementary checks. Replications across model sizes, adaptation methods, and task constructions strengthen the persistence result. The rewrite experiments include aligned-only and random-label controls, supporting the importance of supervision that distinguishes the competing policies.

Critical weaknesses

I am not yet convinced that “objective imprinting” adds enough beyond existing work. Earlier studies already show that models with similar accuracy can use different features and that fine-tuning can preserve reliance on spurious cues [1-2].The controlled training-history experiments are useful, but the two rules are explicitly taught at the start, and later training deliberately provides no examples that distinguish them. It is also unclear how closely this setup reflects ordinary RAG behavior. Table 1 does not include an unmodified selector or one trained on ordinary retrieval data, and the 82.8-point gap is measured only on recoverable ranking errors.

The reported detection rates need clarification. Sections 4.6–4.7 report that 1,000 IID examples detect the policy difference only 54.9% of the time. If the correct-rank cases have identical outcomes, as the reported results suggest, the stated wrong-rank accuracies and detection rule instead give approximately 71.5–73.6%. The same calculation gives almost 100% at 5,000 examples, compared with 90.8% in Table A18. There may be differences in the outcome pool that explain this, but they are not clear from the paper. Since these numbers support the claimed advantage of targeted audits, I would like to see the underlying counts and calculation reconciled.

[1] Underspecification Presents Challenges for Credibility in Modern Machine Learning. JMLR, 2022.

[2] Mechanistic Mode Connectivity. ICML, 2023.

Questions for authors
  • How does an unmodified Qwen2.5-3B selector perform in the true-rank and corrected-rank conditions of Table 1?

  • Can you provide the outcome counts and calculation behind the 54.9% detection rate in Section 4.6?

Reviewer_UjWBOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper investigates whether models with different training histories retain distinct evidence-selection rules after identical subsequent training. Paired models are explicitly trained to follow semantic evidence or a metadata proxy, then receive continuation examples on which both rules agree. The distinction persists through 64,000 shared-example presentations. Fixed-passage rank interventions demonstrate causal metadata dependence and downstream consequences, while weight, activation, and conflict-training interventions characterize the distinction and its editability.

Critical strengths
  1. The metadata intervention is well controlled. The authors change rank metadata while holding passage content, source IDs, and display order fixed. A shared downstream reader further separates source-selection errors from differences in reader quality. These controls make the evidence for metadata dependence convincing within the studied setting.

  2. The evaluation connects evidence use to answer quality. The paired models perform similarly when rank and content agree, yet differ by 82.8 percentage points in downstream answer accuracy on recoverable ranking errors (Table 1). This shows how high retrieval recall and strong agreement-case accuracy can hide consequential differences in source selection, giving a concrete reason to test cases where supporting evidence is available but not ranked first.

Critical weaknesses
  1. The main finding adds limited insight beyond the training design. Models are explicitly trained to follow content or metadata, then receive further training where both rules give the correct label. Their continued use of the initial rule is consistent with ordinary retention under compatible supervision. The paper documents this behavior carefully, but does not clearly establish what “objective imprinting” adds to the explanation. This limits its main conceptual contribution.

  2. The practical value remains untested in conventionally trained selectors. The full-corpus experiment still uses the deliberately trained semantic and proxy selectors. It establishes the downstream consequences of those rules, but does not show whether the audit uncovers substantial failures in ordinary RAG systems or whether conflict training improves their final answers. Evidence from such systems would be particularly valuable given the limited conceptual advance. Without it, the contribution remains largely a controlled demonstration.

Questions for authors
  1. What observation or prediction distinguishes “objective imprinting” from retaining a learned rule under compatible supervision? Which reported result best supports that distinction?

  2. Beyond the growing answer margins in Figure 4, what do the training trajectories show about changes in loss or parameters? How do these measurements help explain why the rule persists, and what role might confidence or loss saturation play?

  3. Does the fixed-passage rank intervention reveal harmful metadata dependence in a conventionally trained selector? Does conflict training reduce that dependence and improve final answer accuracy?

Reviewer_zeqLOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The manuscript investigates the distinction between retrieval recall and actual evidence use, introducing objective imprinting as the persistence of an early-established decision policy under subsequent training that does not distinguish among compatible rules. Using controlled semantic and metadata-proxy policies, factorial evaluations, and full-corpus retrieval experiments, it demonstrates that models with similar observed accuracy can exhibit substantially different evidence-use behavior.

Critical strengths

The manuscript presents a systematic investigation of evidence-use policies through controlled paired-history experiments and causal interventions, providing useful insights into the limitations of retrieval-based evaluation. However, several concerns remain regarding the extent to which the experimental evidence supports the manuscript’s broader claims.

Critical weaknesses

1. Reliance on Explicit Proxy-Target Supervision

The proxy-history models are explicitly trained during the rule-establishing phase to follow metadata rather than semantic evidence. Although this design isolates the effects of different training histories, it does not show whether similar proxy-following behavior arises without explicitly training models to prefer the proxy. The manuscript lacks evaluations of models trained directly on correlated data without an explicit proxy-target initialization, leaving the practical relevance of the induced policies insufficiently validated.

2. Limited Generalizability of the Downstream RAG Evaluation

The reported 82.8-point exact match gap is obtained on recoverable rank errors using a modular selector-reader pipeline over a CounterFact-derived corpus. In this setup, the selector passes only one passage to the reader, and the proxy-history model is explicitly trained to follow rank-1 metadata. Consequently, the large downstream performance gap is largely expected when the supporting passage is ranked below the first position. Without evaluations in more standard multi-passage RAG settings, where the generator recieves all retrieved passages without explicit rank metadata, it remains unclear whether comparable performance gaps occur in practical systems.

3. Insufficient Analysis of Learning During the 64k Continuation

Both semantic- and proxy-history models already achieve 100% agreement-set accuracy before the shared continuation, with high initial answer margins shown in Figure 4(b). Consequently, the persistence observed after 64k shared-example presentations may partly reflect weak learning signals from examples that both models already predict correctly. Although the manuscript tracks policy behavior during the continuation, it does not report how much the model parameters change over this period. Additional analyses of parameter changes or experiments starting from less well-fitted checkpoints would help clarify whether the observed persistence holds under more substantial continued learning.

Questions for authors

Please see the weaknesses above.

Reviewer_imnEOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper argues that retrieval recall, task accuracy, and evidence-use policy are three distinct properties. High recall means the answer-bearing passage reached the context; it doesn’t mean the model used it.

Critical strengths
  1. The idea of looking beyond retrieval recall is important and interesting.
  2. The paper is based on a simple and intuitive hypothesis.
Critical weaknesses
  1. The paper is purely empirical under scenarios that may not be practical. The proxy model is trained to fail. Its 0% support-choice accuracy and 0.111 EM match the rank-1 baseline exactly, so the retrieval experiment confirms the training objective rather than revealing a natural failure. An off-the-shelf or normally fine-tuned reader is needed as a comparison.

  2. The setting is artificial. Rank is given as explicit text and display order is randomized. A test with implicit positional rank, the realistic case, is missing.

  3. The baselines are missing. The paper never tests a model trained only on aligned data, with no warm-up, to see which rule it adopts by default.

Questions for authors
  1. How do you see objective imprinting arising in real RAG training pipelines, where no one explicitly supervises a proxy rule?
  2. How would your conclusions change if rank were conveyed only implicitly through passage position rather than explicit metadata?
  3. Why does BGE make so many more rank errors than BM25 on this corpus?

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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